Like probably many others, we have been waiting eagerly for the
results of the LEGS study (1). The expectation was that this trial would
bring light into the ongoing controversy about the value of chondroitin,
glucosamine, and their combination in the treatment of osteoarthritis (OA)
of the knee, and provide answers to several open questions. The LEGS study
fully met this expectation as to the structure-modifying effect of the
combination of chondroitin sulphate and glucosamine sulphate. However,
what do the results of this trial tell us about the structure-modifying
effect of chondroitin sulphate or glucosamine sulphate alone or about the
symptomatic effect of chondroitin sulphate, glucosamine sulphate, or the
combination thereof? Unfortunately, the results of the LEGS study add very
little to this question as we will point out subsequently.

Symptomatic effect:
The main symptomatic outcome measure in the LEGS study was changed from
the use of NSAIDs to self-reported pain when the authors realized that
only about 20 % of the patients recruited till that point in time were
taking NSAIDs. The alternative primary outcome measure to assess the
symptomatic effect was the maximum score of pain 'at its worst' recorded
daily in a 7-day diary that the participants had to complete every two
months. There are several problems with this alternative outcome measure:
1. It seems not to have been validated, i.e. we have not found any
relevant validation study.
2. Experiences with it are lacking, i.e. we are not aware of any other
trials in which this measure had been used.
3. Pain due to knee OA is activity- related (depending on the activity),
i.e. a patient with knee OA may not suffer from pain while walking, but
may does so when descending stairs. We do not know what activity caused
'pain at its worst' and how long that pain lasted. The activity that
caused 'pain at its worst' likely was not always the same. Pain 'at its
worst', therefore, may be largely an arbitrary measure.
4. Apart from being related to a very specific activity, pain 'at its
worst' may lasted only seconds. Thus, potentially, this measure clinically
may not be very relevant.
5. As 'average pain' - as opposed to 'pain at its worst' - decreases,
patients may dare to indulge in more challenging activities. Such more
challenging activities are likely to cause temporarily similar 'pain at
its worst' even when 'average pain' decreases over time. Therefore, the
alternative outcome measure actually may be more prone to a 'floor
effect', i.e. contribute to what the authors wanted to avoid with its use.
6. We do not know how 'pain at its worst' correlates with 'average pain',
pain on a standard visual analogue scale (VAS), or WOMAC pain, if at all.
7. As 'average' pain on a numerical rating scale is imperatively smaller
than 'pain at its worst', the use of the alternative measure as an
inclusion criterion (4 or more on a scale of 0-10) resulted in a very
mildly symptomatic study population as documented by the WOMAC pain
scores. These scores were between 6.5+/-3.4 (mean+/-SD) and 6.8+/-3.7 on a
scale of 0-20 corresponding to 33+/-17 and 34+/-19, respectively, on a
scale of 0-100. According to the EMA guideline CPMP/EWP/784/97 Rev. 1 (2)
in order to assess the symptomatic effect of a drug, patients must have
pain of at least 40 mm on a VAS of 100 mm. Judging on the basis of the
above scores and SDs only about 30 % of the patients or about 50 patients
per group met this criterion whereas about 100 are needed to observe
statistically significant differences (3), not taking into account the
dilution by those that are not sufficiently symptomatic.

With respect to the assessment of the symptomatic effect we would
like to note also that the information about co-medications as well as
their cessation and washout provided in the publication is very scarce.
From some statements and tables we conclude that there were no
restrictions regarding co-medications. Patients could take paracetamol,
NSAIDs, and opioids at their own discretion (as long as they had been
prescribed such co-medications earlier or during the trial). About 30 % of
the patients had been on a dietary supplement containing glucosamine
during the month before enrolment. Data regarding the use of a dietary
supplement containing chondroitin or a combination of the two before
enrolment is lacking. Thus, most likely there was no washout of potential
effects of such supplements, and it remains unclear whether the patients
actually had been asked to stop taking such supplements during the trial.
Assuming that chondroitin, glucosamine, and the combination of the two
have a symptomatic and a structure-modifying effect, and also carry-over
effects as described in the literature (4), i.e. effects that last to some
extent at least 3 months beyond cessation of treatment, the lack of any
appropriate washout and the possible intake of (additional) dietary
supplements with chondroitin, glucosamine, or a combination of the two are
likely to have influenced the results, particularly those of the placebo
group, and, thus, contributed to a diminishment of the differences between
the active treatment groups and the one with placebo. If so, then this
affected the observation of the symptomatic as well as the structure-
modifying effect. In any case, under the circumstances summarized above,
the authors should not only have adjusted their analysis of the
symptomatic effect for baseline pain and repeated measurements over time,
but at least also for all pain-relevant co-medications and for exercise.
Exercise was potentially a strong confounder, because, according to the
data provided in Table 4, the number of participants with inadequate
exercise decreased in the placebo group whereas it remained more or less
stable in the glucosamine and the combination group, and increased in the
one with chondroitin.

Structure-modifying effect:
The authors decided, a priori, that for valid estimates of joint space
narrowing (JSN), a medial tibial inter-rim distance (TIRD) of <= 1.7 mm
at each time point was required for an X-ray to be included in the
analysis. Furthermore, they limited their analysis to pairs of X-rays with
a difference in TIRD of <= 0.2 mm between the two X-rays. The first
criterion was adopted from work by Vignon et al., 2010 (5). The LEGS study
was registered with ClinicalTrials.gov (NCT00513422) on August 7, 2007,
thus before the publication by Vignon et al., 2010. With 'a priori' the
authors, therefore, mean that their decision to apply the above criterion
had been taken prior to the data analysis. Nevertheless, the application
of this criterion represents a deviation from the original protocol. The
authors, therefore, first should have carried out the analysis according
to the protocol, and also should have published the results of that
analysis. The analysis actually carried out and presented in the
publication could then have served as a sensitivity analysis to
consolidate or question the results obtained according to the protocol and
for discussion.

The protocol allowed a single repeat of each X-ray if the TIRD was
> 2.0 mm. Thus, the limitation of the analysis to X-rays with a TIRD of
<= 1.7 mm is largely redundant. Therefore, it is likely that the
reduction of the number of 'valid' pairs of X-rays predominantly can be
attributed to the application of the second criterion, a difference of
TIRD of <= 0.2 mm between pairs of X-rays. This second criterion is not
only too severe - Vignon et al., 2010 set the cut-point at 0.5 mm and not
at 0.2 mm -, it is also unnecessary: Vignon and co-workers only applied
the second criterion to pairs of X-rays in which both TIRDs were > 1.7
mm. They, however, did not investigate any subgroup of pairs of X-rays
meeting both of the above criteria. In fact, the first criterion is
already sufficient to guarantee a high accuracy and the best
responsiveness. They found a JSN of 0.13+/-0.51 mm (mean+/-SD) over one
year and a standardized response mean (SRM) of 0.25 for all pairs of X-
rays (n=590) as well as a JSN of 0.15+/-0.43 mm and a SRM of 0.34 for all
pairs of X-rays with a TIRD of <= 1.7 mm in both of them (n=256). All
other results in their publication refer to situations where one or both
of the two X-rays of a pair had a TIRD > 1.7 mm. Their results clearly
indicate that the application of the first criterion is absolutely
adequate, and, furthermore, that the gain in accuracy and responsiveness
disproportionately is at the expense of statistical power. Again, as the
loss of 'valid' pairs of X-rays by the application of the first criterion
had not been accounted for in the sample size calculation, the authors
should have carried out the analysis of the X-rays according to the
protocol and then applied the first criterion for sensitivity analysis. As
for the second criterion, there is no evidence that it contributes
anything when applied to pairs of X-rays in which both TIRDs are <= 1.7
mm, with the exception of an unacceptable loss of statistical power.

In summary:
Symptomatic effect: The inclusion of very little symptomatic patients, the
switch of the primary symptomatic endpoint to an unusual, unpredictable,
and not validated alternative outcome measure, and the lack of exclusion
or control of confounding factors do not allow to draw any substantial
conclusions regarding the symptomatic effects of chondroitin sulphate,
glucosamine sulphate or the combination of the two.

Structure-modifying effect: With only about 50 % of valid pairs of X-
rays, i.e. about 75 per group and one third less than required according
to the sample size calculation, the results of the LEGS study as presented
in the publication do by no means exclude a structure-modifying effect of
chondroitin sulphate or glucosamine sulphate alone.

Several characteristics of the LEGS study discussed above are suited
to underestimate or impede the detection of the investigated effects. The
fact, however, that the combination of chondroitin sulphate and
glucosamine sulphate nevertheless did achieve a meaningful reduction in
JSN over 2 years, compared with placebo, in patients with mostly early
radiographic knee OA in this study adds even more weight and importance to
this finding.

Conflict of Interest:

Andreas G. Helg is employed by IBSA Institut Biochimique SA, a Swiss manufacturer and distributor of a chondroitin sulphate
prescription drug and a glucosamine sulphate dietary supplement. Analysis of the publication of the LEGS study and the preparation
of this letter were carried out on behalf of IBSA.

We thank Dr. Iannone et al for their comment on our recent study on drug
survival on etanercept, infliximab and adalimumab in patients with RA.[1]
They noted similarities between our findings and their previously
published data[2] on 853 Italian patients starting TNF inhibitor treatment
in 2003-2004 in terms of best drug survival on etanercept, similar 4- vs 5
-year drug survival for etanercept and infliximab, and some shared
findings regarding predictors. We agree that there are several
similarities, but also differences. We also apologize for not including
their study in our non-exhaustive review in the appendix, and not citing
their study together with the study by Kievit et al.[3]

Specifically, we investigated whether drug survival differed between the
selected TNF inhibitors, whether these differences were modified by time
on treatment, and whether discontinuation rates have changed across
calendar periods. We also looked at predictors of drug discontinuation. We
did this in more than 9000 prospectively followed patients who initiated
their first biologic treatment between 2003 and 2011.

We found, similar to many previous European investigators (including
Iannone et al)[3-8], that etanercept had the best drug survival in overall
analyses. We did, however, find that the difference was modified by time,
with etanercept being superior to adalimumab only the first year.
Interestingly, Iannone et al show data potentially supporting our finding
of effect modification by time, although they provide no statistical test
of what could be a greater difference in the first and second year
(compared to later years) between etanercept and adalimumab.

Regarding predictors of drug discontinuation, we used Cox regression when
evaluating age, sex, education level, calendar period, HAQ, concomitant
DMARD use, disease duration, and two measures of general frailty. All
variables but age were statistically significant predictors in the
multivariable model, although the magnitude was small to moderate for
most. Iannone et al investigated predictors using stepwise logistic
regression, and it is unclear whether or how they took censoring into
account. In contrast to our findings, they could detect few statistically
significant independent predictors, although disease duration and
concomitant DMARD use were statistically significant, similar to our
findings.

Considering the recognition of the importance of contextual factors (such as the number of alternative treatment options available)
on the real-world effectiveness and drug survival of existing treatment options in RA, we welcome further studies of drug
survival and predictors for long-lasting response to therapy.

I read with interest the paper by Vital el al. (1), a pilot study
testing the efficacy of an extra dose of rituximab (completing 3x1000 mg
over four weeks) in comparison to the standard-dose regimen (2x1000 mg) in
rheumatoid arthritis (RA) patients with incomplete depletion of B cells
after a first 1000 mg dose of RTX. The study represents an advance in the
knowledge about the effects of rituximab, but I have some concerns about
the interpretation of the results.

The overall analysis of the efficacy outcomes at week 28 (when no
patient had yet received a repeat course of rituximab) did not favor the
extra-dose regimen. Good EULAR response, EULAR remission, ACR50 and ACR70
responses were numerically (but not statistically) better in the standard-
dose group. After 28 weeks, the efficacy results are difficult to
interpret, because imputation of no response for ACR20 and EULAR responses
was used for patients presenting reactivation of disease (i.e., a DAS28
increase >0.6), even if they improved after a repeat course of RTX.

The authors commented in the abstract that the extra dose of RTX
produced no worsening in safety. However, the study is clearly
underpowered to detect safety problems due to the small sample sizes. At
12 months, infections and serious adverse events (SAE) were more incident in the extra-dose group (rate ratios 1.42 [95% CI
0.65, 3.17] and 4.33 [95% CI 0.43, 231.41], respectively), although the differences were not statistically significant. The
incidence of SAE in the extra-dose group (33/100 patients/year) is numerically higher than the expected based on historical
data of RTX therapy (14.4/100 patients/year [2]).

Recent evidence (3,4) has suggested that low-dose RTX (2x500 mg or a
single infusion of 1000 mg) has an efficacy that is noninferior to the standard dose (2x1000 mg) of RTX, and is possibly safer.
Aiming at complete depletion of B
cells using an extra dose of RTX may possibly lead to a higher incidence of late-
onset neutropenia (5), hypogammaglobulinemia (6,7), and serious
adverse events, which may reduce the effectiveness and increase the costs
of the treatment of rheumatoid arthritis with RTX.

The ethical consideration in placebo-controlled studies of
antirheumatic drugs is of primary importance. We thank Dr Yazici for his
questions regarding the ethical aspect of our study.

The GO-MONO study was designed to have placebo crossover to
methotrexate (MTX) at Week 16, as a Registration Study to Japan Health
Authority, following the MHLW Guideline for the Clinical Study and
Evaluation of Drugs for Rheumatoid Arthritis, which is similar to the US
Food and Drug Administration's Guidance for Industry Rheumatoid Arthritis
(1). The US guidance recommends sponsors to limit the use of placebo as a
control and consider the use of an active comparator as the control or the
escape to rescue treatment in studies longer than 12 weeks. In the event
of aggravation of rheumatoid arthritis (RA) symptoms, subjects were to be
withdrawn from study immediately and receive appropriate rescue treatment,
which was explicitly written in the informed consent. The investigators
and IRBs of the participating medical institutions and the Japanese health
authorities considered that the GO-MONO study had adequate ethical
considerations. Twelve or 24-week placebo-controlled studies were
conducted in the clinical development of recently approved antirheumatic
drugs in Japan after the golimumab studies without being questioned about
the ethical conduct (2,3,4).
Even allowing for the disadvantages in subjects receiving placebo,
conducting a placebo-controlled study of golimumab monotherapy was thought
to be imperative not only because it would meet the requirement by the
Japanese health authorities to demonstrate the true efficacy of an
antirheumatic drug in a placebo-controlled study, but because the approval
of golimumab monotherapy provide an alternative treatment option to MTX-
intolerable patients with active RA.

The second issue Dr Yazici raises is the credibility of the data from
our studies based on the different results for the effect on radiographic
progression between the studies.

As we discussed in the paper describing our earlier 2 studies of
golimumab (5), subjects in all treatment groups of the GO-FORWARD study
had lower disease activity and less radiographic progression at baseline
than those in the earlier studies of TNF-? inhibitors in patients with an
inadequate response to MTX (6,7,8), and this may have resulted in the lack
of statistically significant differences between treatment groups. The GO-
FORWARD study failed to adequately assess the effects of golimumab on
radiographic progression in patients with established disease, In the GO-
MONO study, however, subjects had more active RA inflammation at baseline
than those in the GO-FORWARD study, and golimumab showed a significantly
greater effect of preventing radiographic progression. This result is
consistent with the results in our other studies of golimumab, the GO-
FORTH study (9) and the GO-BEFORE study (10). A similar relationship was
seen between the radiographic progression and response to certolizumab in
patients with active RA despite MTX (11).
Dr Yazici points out that radiographic benefit was not demonstrated with
golimumab until post hoc analysis of the data was done. As explained in
the literature of the GO-MONO study, the post hoc analysis using
normalized data was appropriate for radiographic analyses because the
radiographic change scores were not normally distributed. For instance,
the median of the golimumab 100 mg group was skewed because of a single
outlier. Data normalization is the standard statistical analysis technique
used in the literature and for Health Authority submissions. Significantly
less radiographic progression than placebo was noted when the data were
analyzed post hoc using normalized scores. The 100 mg dose was associated
with better clinical outcome than the 50 mg dose (not statistical
comparison) as measured using the American College of Rheumatology
criteria and Disease Activity Scores. The effect of the 100 mg dose for
the use in golimumab monotherapy was appropriately evaluated and approved
by the Japanese health authorities.

Although we generally agree with Dr Juanos-Iborra et al [1] who noted
that some of the most common manifestations of Erdheim-Chester disease
(ECD) at time of onset (such as skeletal, constitutional or even
neurological symptoms) may lack adequate specificity for a timely and
prompt diagnosis, it is conceivable that the same manifestations, if
unexplained, may often lead to further imaging and histological studies,
which will eventually suggest a correct diagnosis. Undoubtedly, as the
authors themselves stated and as highlighted in our recent study published
in Annals of the Rheumatic Diseases, other more typical manifestations of
ECD, such as the radiologic evidence of 'coated aorta', of 'hairy
kidneys', or of 'pseudotumoral' infiltration of the right atrium, as well
as the typical bone scan finding of a symmetrical and abnormally increased
uptake in the distal ends of long bones, should be clearly indicative of
the disease [1-3]. However, our study and others, including the
descriptions of the largest reported cohort of patients with ECD,
highlighted a striking diagnostic delay (up to 29 years) even in those
patients presenting with the aforementioned typical manifestations [3-5].
To allow a more timely diagnosis, we believe that the broader medical
audience should be privy to both the specific and sensitive manifestations
of this protean and multifaceted disease. Encouragingly, it has been
observed that the average diagnostic delay for ECD has dramatically
shortened in the recent years because of a better recognition of the
disease [6]. As Sir William Osler said, "many diseases [...] are seen so
rarely and yet are so distinctive, requiring only to be seen to be
recognized, that it is incumbent upon members to use the [medical] society
to show such cases" [7].

We read with interest the article 'In erosive hand osteoarthritis
more inflammatory signs on ultrasound are found than in the rest of hand
osteoarthritis' by Kortekaas et al [1]. The authors found that
interphalangeal joints of erosive osteoarthritis (EOA) patients, with
erosions being defined by conventional radiography (CR), demonstrated more
sonographic inflammatory changes in adjacent non CR-eroded joints compared
to patients without EOA. This may give the impression that a joint
showing erosions on hand CR points towards a more severe generalised
inflammatory phenotype and we would like to clarify this.

We are unsure what the significance and robustness of these
observations is, given the increasing pathophysiological understanding of
hand osteoarthritis that has emerged from high-resolution MRI [2, 3], that
overcomes problems encountered in ultrasound including overlying
osteophytes that may obstruct views of erosions. Utilising 23mm
'microscopy' surface coil to study early hand osteoarthritis and compared
to CR, we found 4 times more erosions were detected on MRI, in particular
marginal erosions that lay within the joint capsule, but beyond the
margins of the articular cartilage (1 on CR, 19 on MRI, p<0.05).
According to Kortekaas et al, EOA was defined by one or more erosions on
CR at the interphalangeal joints. The limitation of CR in determining
erosions is due to its 2-dimensional capability and inability to detect
very small erosions. However the sensitivity of MRI can potentially
increase the number of joints considered as true EOA compared to CR by a
factor of 4 [2]. As Kortekaas et al acknowledge in their discussion
ultrasound has also been shown to be more sensitive to the detection of
erosions in EOA than conventional radiography in recent studies [4]. We
believe that most published prevalence of EOA may be under-estimated due
to the relative insensitivity of CR used for diagnosis. In a nutshell, it
is likely that many of the joints the authors term non-erosive on CR,
actually have extensive pathoplysiologically identical, but smaller,
lesions in adjacent "non erosive" joints.

Of particular importance our study demonstrated that enhancing
synovitis post contrast, akin to that seen in inflammatory arthritis such
as rheumatoid or psoriatic arthritis, was present in all cases and filled
the erosion on MRI, further supporting the idea that non-radiographic hand
OA inflammation is linked to erosions [2]. We have previously shown on
histology that synovial tissues do line the surface cavity of bone
erosions, which potentially can be subjected to an inflammatory process
[5]. So we envisage that the joints that have power Doppler synovitis on
ultrasound but no radiographic erosions observed by Kortekaas et al may
also have a high likelihood of being erosive had cross sectional
modalities been used to categorise them.

We agree with the authors that their cross sectional study is unable
to clarify if the inflammation observed in EOA may lead to further erosive
changes. However work showing that suppression of inflammation with anti-
TNF halts erosive progression in hand OA, suggests that uncontrolled
inflammation in non-erosive hand OA does progress to radiographic EOA [6].
We argue that the observation by Kortekaas et al was limited by the lack
of sensitivity of the imaging modality (CR) used to call EOA. Therefore
the sonographic changes of inflammation in hand OA joints are likely to be
already strongly linked to erosion in the same joints.

Despite significant efforts and advances in the field of autoimmune
diagnostics, the standardization and proper use of antinuclear antibody
(ANA) testing in clinical practice remains a challenge. In 2013, important
contributions attempting to clarify and add rigor to this area have been
published [1, 2]. In particular, the recent recommendations published by
Agmon-Levin et al. [1] address very important issues that confront
contemporary laboratory medicine. Using a Delphi approach, the authors
generated 25 recommendations for the detection of anti-cellular
antibodies, previously referred to ANA and anti-dsDNA antibodies. In a
second important paper, Bossuyt and Fieuws reported added value of solid
phase assays [2]. Considering the high impact of published recommendations
and associated editorials, careful verification, validation,
clarification, education and, if necessary, adjustments are crucial. Some
of the recommendations requiring further clarification are summarized in
Table 1 or discussed in the text.

Terminology of diseases and autoantibodies
Agmon-Levin et al., make an exceedingly important point with respect to
the nomenclature of autoantibodies found in systemic autoimmune rheumatic
disease (SARD) sera is inconsistent, misleading and/or not in keeping with
contemporary cell and molecular biology terminology. The terms 'anti-
nuclear antibodies' (ANA) and 'extractable nuclear antigens' (ENA) are no
longer technically correct and do not cover the entire spectrum of
relevant autoantibodies. 'ANA' using indirect immunofluorescence (IIF) as
well as some other screening assays detect antibodies directed against
nuclear and non-nuclear elements (as in their recommendation 13), while
'ENA' may refer to some antigens that are neither extractable nor nuclear.
Therefore, it is highly desirable to change these terms to more
appropriate and informative ones, such as anti-cellular antibodies and
specific antibodies, respectively. Such a change in nomenclature requires
broad agreement and adoption within the broad stakeholder medical
community and then a transition period, as most manuscripts and textbooks
would continue to use the older 'classic terms'.
In addition to the autoantibody terminology, a new terminology for
connective tissue disorders is also required. In their recommendations,
the authors used the term SARD without specifying which diseases should be
included in this group. Recently, the term ANA associated rheumatic
disease (AARD) was introduced [3]. Although this term uses the
inappropriate abbreviation `ANA`, this terminology or a slightly modified
version might be preferred and should include systemic lupus erythematosus
(SLE), Sj?gren's syndrome (SjS), systemic sclerosis (SSc) and idiopathic
inflammatory myopathies (IIM). Rheumatoid arthritis (RA) is thought of as
a SARD by some because it clearly has critical extra-articular
manifestations. However, since only a subpopulation of RA patients has a
positive ANA, and because other serological markers such as anti-
citrullinated protein antibodies (ACPA) and rheumatoid factor (RF) have
more clinical utility, RA should not be included in the AARD group.
Changing the terminology of a disease is a challenge and requires careful
considerations, but evolving knowledge about disease phenotypes, disease
specific biomarkers and pathogenesis makes a review of disease
nomenclature mandatory. Recently, it has been suggested that the
nomenclature of SSc might be adjusted to one based on serological markers
and autoantibodies [4] and the names of several autoimmune mediated
diseases including granulomatosis with polyangiitis (GPA, formerly known
as Wegener`s granulomatosis) have been changed.

Change in referral patternHistorically, primarily rheumatologists and clinical immunologists ordered
ANA testing as an aid to the diagnosis of systemic lupus erythematosus
(SLE) [5]. Much of this was due to the embedding of ANA and certain ENA in
the older [6] and now more recent [7] classification criteria for SLE.
Nowadays, a broad spectrum of clinicians order the ANA test including but
not limited to rheumatologists, internists, dermatologists, nephrologists,
oncologists, cardiologists, neurologists, gastroenterologists,
psychiatrists and even primary care physicians. This can be attributed to
the appreciation that the ANA test has clinical value in multiple diseases
including autoimmune liver diseases such as autoimmune hepatitis and
primary biliary cirrhosis (PBC), and might also provide clinical
information in vasculitis, inflammatory bowel disease (IBD), a widening
spectrum of autoimmune neurological diseases and malignancies. This has
significant impact on the pre-test probability and an even more pronounced
effect on the post-test probability of the ANA test. An important aspect
for the use of ANA is the likelihood ratio SARD. Using this information,
calculation and understanding of the post-probability of disease based on
the respective patient population should be a vital part of the diagnostic
process [8].

Methods for ANA detection and sensitivity and specificity of ANA testingAlthough significant improvements have been made and several solid phase
assays are available for ANA detection, the IIF HEp-2 method was recently
recommended as the method of choice for ANA detection [9].

The authors
recommended that a serum screening dilution yielding 95% specificity
should be selected in each laboratory based on the respective patient
population. On the same note, they also point out that the sensitivity in
SLE should be >90% [1]. Although historical data demonstrate such high
diagnostic accuracies [10], more recent data do not support a diagnostic
accuracy of a combined 90% sensitivity and 95% specificity [2, 11]. Based
on a large population based study it was reported that 13.8% of apparently
healthy individuals were ANA positive at a screening dilution of 1:80
[12]. Since this study used commercial HEp-2 substrates but a clinically
unvalidated secondary antibody and did not include SARD patients, further
studies with large patient cohorts are needed.

Limitations of the IIF test and lack of standardizationThe authors also acknowledged that the IIF ANA test lacks sensitivity for
several clinically relevant autoantibodies including but not limited to SS
-A/Ro60, Ro52/TRIM21, ribosomal P and Jo-1 [1]. Although related
observations have been published [5], further emphasis and education is
needed to ensure that laboratorians and clinicians are fully aware of this
limitation. Not addressed in detail is the variability of HEp-2 kits from
different manufacturer in terms of sensitivity and specificity as well as
IIF pattern interpretations. Although a study along these lines has been
previously reported [6], evidence from systematic and multi-center studies
analyzing the sensitivity and specificity of various contemporary
commercial HEp-2 kits seem are missing.

Added value of solid phase immunoassaysBossuyt and Fieuws [2] showed that adding a solid phase assay (SPA) to the
IFA HEp-2 testing algorithm increased the diagnostic utility for SLE, SjS
(all samples on both assays) and SSc (all samples by IIF and positives by
SPA). However, this likely would have impact on health care costs and, in
many jurisdictions, only one ANA test is reimbursed, limiting the parallel
approach using IFA and SPA for ANA testing. However, early and accurate
diagnosis and then appropriate treatment of patients with AARD are
important aspects of favourable clinical outcomes, although they also have
significant benefits for the health economy. A delayed diagnosis is
attended by the dangers of higher morbidity and mortality due in large
part to irreversible tissue damage while false positive results may lead
to unnecessary referrals, misdiagnosis or even inappropriate treatment [5,
13].

Clinical association of indirect immunofluorescence patterns and
autoantibodiesIn Table 2, the authors list anti-CENP-F antibodies as a target structure
of anti-centromere antibodies and describe this autoantibody as associated
with SSc and Raynaud's phenomenon (RP). However, anti-CENP-F antibodies,
in contrast to anti-CENP-A/B/C antibodies, are not associated with SSc and
RP. Approximately 50% of patients with anti-CENP-F antibodies have a
malignancy [14]. In addition, the IIF pattern associated with anti-CENP-F
antibodies is distinct from the classical centromere staining pattern.
Anti-CENP-A/B/C antibodies stain multiple nuclear dots in interphase and
mitotic cells while anti-CENP-F antibodies produce a cell-cycle dependent
pleomorphic pattern [15]. Additionally, although historically known as a
marker for SLE, anti-PCNA antibodies have recently been found in various
conditions and their disease association has been questioned [16, 17].
Therefore, further studies are needed to re-validate the clinical
association of anti-PCNA antibodies. Lastly, it is correctly noted that
anti-Ro60 and anti-Ro52 antibodies impart different clinical meaning [18,
19]. Notably, another aspect concerning anti-SSA/Ro antibody is the
detection of its variants directed at SS-A/Ro60 and Ro52/TRIM21, as some
tests currently include only the SS-A/Ro60 antigen [18]. Detection of anti
-SSA/Ro is recommended in different clinical scenarios including
counselling of patients with autoimmune disease who contemplate a
pregnancy. The latter are mainly related to anti-Ro52/TRIM21 antibodies in
neonatal lupus syndrome [18]. Therefore, specifying the antigen used and
evaluation of both anti-Ro52/TRIM21 and anti-SS-A/Ro60 should be
considered.

Concluding remarksWith emerging novel disease modifying drugs for autoimmune diseases, the
autoantibody response and levels might change over the course of the
disorder, which also might impact the utility of certain assays.
Additionally, disease criteria and activity scores evolve which also can
impact the performance of autoantibody assays. Therefore, large studies
using well defined patient cohorts (such as the Systemic Lupus
International Collaborating Clinics (SLICC)) are needed to re-evaluated
anti-cellular and anti-dsDNA antibody assays for clinical use.

In their comments about our systematic review on cardiovascular (CV)
comorbidities in patients with psoriatic arthritis, (1) dr Gonzalez-Gay
and colleagues, point out that in their studies, (2,3) in contrast to our
Table 4, they did demonstrate a correlation between inflammatory
parameters and flow-mediated dilatation (FMD) or intima media thickness
(IMT). This is indeed correct when these tests are correlated with
inflammatory parameters at the time of diagnosis. However, we felt that it
is more appropriate to correlate the inflammatory parameters with the time
when the (functional) vascular testing was done. Then the correlations of
FMD and inflammatory parameters were not statistically significant (Table
3). (2)
Similarly, univariate analysis revealed no significant correlation between
DAS28, ESR/CRP (at time diagnosis or at time of testing) with IMT (Table
2), (3) as also indicated in our Table 4, albeit that one may argue that
some sort of AUC measure should have been used as IMT is more a reflection
of a cumulative atherosclerotic burden.
Finally, we fully agree with dr. Gonzalez-Gay and colleagues that further
studies are needed that investigate if and to what extent anti-
inflammatory treatment and/or modification of CV decreases the CV risk in
patients with PsA.

In his letter, Jan Damoiseaux plees for testing of anti-RNA
polymerase III antibodies (ARA), and also other (novel) SSc-associated
antibodies, only for those patients who are really suspected for SSc.
Damoiseaux argues that there is a necessity to provide clinical
information together with the request for testing for rheumatic systemic
autoimmune diseases.

We very much agree that testing for SSc-associated antibodies should
only be requested for those people who really are suspected to have SSc.
We feel that a correct request of testing for these auto-antibodies is
first and foremost a responsibility of the requestor, i.e. the
rheumatologist. However, immunologists and rheumatologists almost
certainly can learn from each other in optimizing requests for antibody
testing, which admittedly also may mean fewer requests but therefore for
the right people at the right moment.

Curiously enough, in his letter Damoiseaux says that 'it is to be
questioned whether inclusion of ARA was valid' and further he brings
forward that '25x more false-positive ARA results are to be expected than
true positives'. We do not agree with both of his points.

Indeed in the derivation cohort of 100 SSc patients and 100 controls
with diseases similar to SSc, the occurrence of ARA positivity was
extremely low, and consequently there was no difference between SSc
patients and controls. While being eyebrow-raising (at least to us), it
would have been an error to discard ARA for this reason solely, as the
validation set showed later. ARA was included because many other studies
showed its relevance in recognizing SSc (external knowledge) and because
of the systematically assessed opinion of expert clinicians in SSc.
Finding outlying results on a single item in a sample of this size most
likely is the result of sampling error; which is uncomfortable, but no
reason to question the inclusion of ARA as not valid. In the validation
sample, 27/268 (10%) SSc patients were ARA positive, towards zero ARA
positive patients in the 137 consecutively collected patients with a SSc-
like disorder.

Second, in his reasoning, Damoiseaux states that in routine
laboratory settings it is realistic to expect that only 2 out of each 1000
patients being suspected for systemic autoimmune rheumatic diseases, and
thus are tested for autoantibodies according to local algorithms,
eventually are diagnosed with SSc. Damoiseaux shows in his calculations
persuasively that ARA is not suitable as a screening test. However, while
a SSc/non-SSc ratio of 2/1000 probably may be realistic it can be debated
whether that is usual in practice. Many referral centres for SSc may have
patient domains with higher a priori probabilities for SSc than 0.002.

If we argue for example that ARA is ordered only when suspecting SSc
and that in those situations it may be that non-SSc diseases are 5 times
more prevalent and ARA specificity is only99%, then for every 100 SSc
cases there would be 500 non-SSc cases with 5 positives while in the SSc
cases there would be 11 positives (if we accept 11% sensitivity). Then
there would be no where near 25 times more false positives.

We feel it is the responsibility of the rheumatologist to select
those patients with a sufficiently high probability to have SSc for
further testing. Notably, the SSc classification criteria for SSc consist
of a number of items, including SSc-associated antibodies, that together
inform of the probability of SSc being present. In diseases of the
syndrome-type like SSc, it is difficult to interpret tests in isolation.

We thank Aramugakani et al. for their critical reading of our
Editorial (1) accompanying Cheng et al. paper on the role of long-lived
plasma cells (PC) in driving murine lupus nephritis (LN) (2). First, we
obviously share - and explicitely mentioned - the safety issues related to
long-lived PC depletion, in particular a possible high infection rate.
Second, our purpose was not to question the effects of rituximab on anti-
dsDNA production in active lupus patients, in particular when complete B-
cell depletion is achieved (3), nor the importance of targeting
plasmablasts and short-lived PC in acute lupus. Rather, we stressed that
long-lived PC, including those homed in previously injured tissues, may
well be responsible for relapses (sometimes after long periods of clinical
and serological inactivity). In this respect, successful targeting of
these cells may potentially offer a cure, as could be the case with
haematopoietic stem cell transplantation. Finally, we agree that
combination (or sequential) therapy with agents targeting both
plasmablasts/short-lived PCs and long-lived PCs would make sense from a
theoretical viewpoint, with the obvious caveats regarding infections.